Removable Defects: The Economics and Limits of Deliberate Deficiency

Behavioral contamination detectors can return "no evidence" either because a benchmark is clean or because the audit has little power. We formalize this distinction for a benchmark in which an unknown fraction alpha of items was seen during training. With matched clean and seen controls, the behavioral channel is the sparse mixture Q_alpha = (1 - alpha) P_0 + alpha P_1, and an exact second-moment argument shows that detectability is governed by alpha * rho * sqrt(m), where rho^2 = chi^2(P_1 || P_0) measures behavioral separability. Any scalar detector reduces to its efficacy, ef = |E_1 f - E_0 f| / sqrt(Var_0(f)) <= rho, which can be estimated from controls before the audit is run. A separate sample-split certificate lower-bounds alpha distribution-free, without requiring an orientation assumption. Our empirical finding is two-sided. Frozen calibration efficacy predicts held-out power curves, with R^2 = 0.83-0.98 across six exact-permutation channels, but the efficacy-only Gaussian budget is miscalibrated at the small sample sizes it prescribes, failing in 9/9 gate-passing channels even though efficacy itself transports. The failure is in the inversion, not the calibration. A predeclared two-stage planner that simulates the deployed test repairs the budgets, is uniformly conservative, and abstains when its probe does not transport. The certificate is valid but vacuous at audit scale, and a five-seed paired injection study recovers the mechanism ordering verbatim > paraphrase > surface, in which the apparent answer-only signal is explained by baseline drift. We report the audit contract and its failures together: a non-rejection is interpretable only alongside the efficacy, budget, and validity gates that produced it.

Industrial inspection pipelines often restore a measured image before a detector acts on it, yet restoration can suppress detector-supported defect structure or create clean-region activations. We formulate restoration as a selective action problem over the measured display, five restored candidates, and review. SafeRestore ranks candidates with action-specific fitted scores, chooses a gate on threshold-tuning data, and evaluates the fixed gate on a disjoint certification sample with two one-sided exact binomial bounds: one for the positive-conditional evidence-loss incident rate and one for the all-accepted excess-activation incident rate. The guarantee is marginal for one policy fixed before its certification outcomes are observed, under an image-level i.i.d. working model. In a retrospective split-sample study of 4,591 public Carinthia-S images, the protocol yields auditable risk-coverage behavior. The primary all-action policy passes in one of five training repetitions (12.0% +/- 26.9% pass-gated test coverage when failures count as zero), whereas fixed bicubic and reduced-complexity variants pass more often. On reserved morphologies, evidence-loss incidence rises to 81.1-90.3%, and KolektorSDD lacks both detector competence and enough positive certification images for the stated target. The contribution is therefore an auditable, detector-relative framework for deciding when a transformed image may be returned automatically and when review remains necessary -- not a claim that adaptive routing outperforms simpler policies on the present evidence.

Detectors for GNSS radio-frequency impairments (jamming, spoofing, multipath) are usually reported with a single AUC measured on the distribution they were tuned on. That number falls once conditions move, and the size of the drop is rarely known in advance because labelled field data is scarce. We ask whether this optimism can be predicted before any out-of-distribution data is seen. On an open, parameter-grounded synthetic testbed with a tunable severity shift, we evaluate thirteen detectors (five physics baselines, full-feature logistic regression and multilayer perceptrons, and single-feature learned controls) across four impairment classes. The optimism gap, the difference between in-distribution and shifted AUC, grows monotonically as the shift deepens (mean Spearman correlation 0.50). It is driven by how many observables a detector uses rather than by whether it is learned, and it varies systematically by class. Centrally, a ridge model built only from in-distribution score statistics predicts the gap for a detector it has never seen (R^2 = 0.47) and for an impairment class it has never seen (R^2 = 0.46); both are significant against a 2000-fold permutation null (p < 0.001) and survive removing the feature that is, by construction, part of the target. The headline findings are synthetic. We then run the pre-registered protocol on three open field corpora: on Jammertest 2024 the cross-detector prediction holds (R^2 = 0.11, p = 0.009), and on SatGrid, whose spoofer power sweep gives a calibrated severity axis, in-distribution AUC overstates higher-severity AUC by up to 0.22 and to the point of sign inversion, with in-distribution AUC and realised gap perfectly rank-correlated (Spearman rho = 1.0). The mechanism survives contact with real data, at smaller magnitude than in simulation. We release the testbed, a software-receiver front end, the ingest adapters and the protocol.